First in a prospective series of my own versions of the best arguments for conclusions I don’t personally share. I’m supposed to stick to statements that I believe are true, even if I don’t think they warrant the conclusion. The idea is to probe presuppositions, put our ideas to the test, and of course to implicitly diss the less-good arguments for things we don’t believe. And who knows, maybe we’ll come up with arguments that are so great we’ll change our minds! (By slipping into the royal “we” I’m encouraging others to play along.) So here we go: the best argument I can think of for why research on string theory is a waste of time.

Traditionally, the greatest progress in physics has come through an intense interaction between theory and experiment. We have learned new things when experiments were good enough to bring us data that didn’t fit into the models of the time, but our theoretical understanding was also sufficiently developed that we had the tools to formulate useful hypotheses. While we know that classical general relativity and quantum mechanics are fundamentally incompatible and must someday be reconciled, straightforward dimensional analysis suggests that detailed experimental information about the workings of such a reconciliation (as opposed to true-but-vague statements like “gravity exists” or “spacetime is four-dimensional on large scales”) won’t be available at energies below the Planck scale, which is hopelessly out of reach at the current time.

A defensible response to this lack of detailed experimental input would be to place the problem of quantizing gravity on the back burner while we think about other things. And this was indeed the strategy pursued by the overwhelming majority of theoretical physicists, up until the 80’s. Two things caused a change: the drying-up of the river of experimental surprises that had previously kept particle theory vibrant and unpredictable, and the appearance of string theory as a miraculously promising theory of quantum gravity. Even though the Planck scale was still just as inaccessible, string theory was so good that it became reasonable to hope that we could figure it all out just by using brainpower, even without Planckian accelerators.

But it hasn’t worked out that way. Gadflies point to the landscape of low-energy manifestations of string theory as the nail in the coffin for any hopes to uniquely predict new particle physics from string theory. But that is only a subset of the more significant challenge, and understanding particle physics beyond the Standard Model was never the primary motivation of most string theorists anyway — it was quantizing gravity.

The real problem is that string theory isn’t a theory. It’s just part of a theory, and we don’t know what that theory is, although sometimes we call it M-theory. As Aaron explains in a very nice post, the thing we understand is “perturbative” string theory, which is a fancy way of saying “the part of M-theory where small perturbations around empty space act like weakly-interacting strings.” We’ve known all along that colorful stories about loops of string propagating through spacetime only captured part of the story, but we’re beginning to catch on to how difficult it will be to capture the whole thing. The Second String Revolution in the 90’s taught us a great deal about M-theory, but it’s hard to know whether we should be more impressed with what we’ve been able to learn even without experimental input, or more daunted by the task of finishing the job.

Within our current understanding of string theory, there is not a single experiment we can even imagine doing (much less actually, realistically hope to do) that would falsify string theory. We can’t make a single unambiguous prediction, even in principle. I used to think that string theory predicted certain “stringy” behavior of scattering cross-sections at energies near the Planck scale; but that’s not right, only perturbative string theory predicts such a thing. “String theory” is part of a larger structure that we don’t understand nearly well enough to make contact with the real world as yet, and it’s completely possible that another century or two of hard thinking won’t get us to that goal. It made sense to be optimistic in the 80’s that there was enough rigidity and uniqueness in the theory that we would be led more or less directly to contact with observation; but that’s not what has happened.

The best reason to think that research on string theory is largely a waste of time is because it’s just too hard.

Pretty convincing, eh? But I don’t buy it, even though I think I’ve adhered to my self-imposed rule that I believe every individual sentence above. It might turn out to be the case that another century or two of hard thinking won’t get us any closer to connecting string theory with the real world, but I don’t see any reason to be that pessimistic. The thing that’s really hard to get across at a popular level is that the theory really is rigid and unique, deep down; it’s the connections between “deep down” and the world around us that are the hard part. Count me as one of those who is more impressed with what we have learned than daunted by what we haven’t; if I were to bet, I would say that more thinking will continue to lead to more breakthroughs, and ultimately a version of M-theory that can rightly be called “realistic.”

In the meantime, the advent of sexy new data from the LHC and elsewhere will draw a certain fraction of brainpower away from string theory and into phenomenology, but there will be plenty left over. The field as a whole will fitfully establish a portfolio of different approaches, as it usually does. And there will undoubtedly be surprises around the corner.

the Ancient Philosophers used to sit on a stone all day and think and think and think and they came up with very beautiful and elegant theories which were all wiped out in the Age of Empiricism.

http://evolutionarydesign.blogspot.com/ island

Research on String Theory is a Largely Waste of Time

Because it simply isn’t necessary.

http://arunsmusings.blogspot.com Arun

I think it is now settled that string theory is not a theory of everything and it still aspires to be a theory of something. Research done with that firmly kept in mind is quite OK by me. What was wrong prior to Smolin, Woit et al was the constant insistence that string theory as it currently is applies to reality. It is rather different from the (perhaps well-founded) hope that string theory will one day be connected to reality.

So instead of arguing, let me ask – what are the most bizarre 4-large 6-compactified dimension worlds that can appear in the landscape? This requires a definition of “bizarre” I guess, but perhaps that too is a subject for discovery. The underlying purpose would be to see one can come up with a guess as to a physical principle that ought to exist in order to rule out such worlds.

Pedant

” Research on String Theory is a Largely Waste of Time ”

That’s going to annoy me for the rest of the week… Fix it!

Eric

Arun,
I think it’s more correct to say that string theory gives us pieces of the theory of everything. All of the pieces have yet to be put together and some remain unknown.

Eric

Arun,
I think it’s more correct to say that string theory gives us pieces of the theory of everything. We have yet to put all of the pieces together and yet more pieces which are currently unknown may be required.

http://evolutionarydesign.blogspot.com/ island

string theory gives us pieces of the theory of everything

hahaha… prove it.

Pete Martinez

I do not know whether string theory is the right approach to understanding reality at its smallest, and for reconciling particle physics with the theory of relativity. However, there is no doubt that we will figure this out for the simple and compelling reason that we are hard wired to do so. In a novel I wrote I have the major character makes this point through the aphorism that, “Life knows life.”

http://ksjtracker.mit.edu Charlie Petit

It’s probably been made before, but here’s an outsider’s suggestion: Proclaim string theory (or hypothesizing or whatever) a branch of mathematics. Poof – problem solved. No worries about legitimacy embarrass mathematicians just because their fascinations have no practical ap (yet). I’m a little shaky on history, but wasn’t Riemannian geometry, among other non-Euclidian geometries, a perfectly respectable line of exploration over at the Math Dept. before Einstein and other relativity pioneers used it to practical effect? And there’s no reason a physicist shouldn’t hone his or her math synapses by looking into pure-math fields — esp. those that seem, even hazily, resonant with the universe’s behavior.

http://www.math.columbia.edu/~woit/wordpress Peter Woit

Sorry Sean, but this reads much more like an argument for string theory research rather than one against it…

A few quick comments, maybe I’ll write something later on my blog about other aspects of the “string theory is just too hard” idea.

1. “understanding particle physics beyond the Standard Model was never the primary motivation of most string theorists anyway”

It really isn’t true that what happened in 1984 was all about the sudden appearance of an excellent theory of quantum gravity. Take a look at the highly cited papers from that era, and you’ll find little about quantum gravity, but a lot about compactification schemes for getting the Standard model. The people who made string theory a hot subject were mostly particle theorists excited by the the idea of a unified theory, with real predictions seemingly possible by looking at the lowest energy states of a superstring propagating on a compactified 10d space-time. They were well aware that making experimental contact with quantum gravitational effects was almost certainly hopeless, and these were people highly concerned with doing research that did have experimental implications.
It was only much later, as hopes for getting particle theory our of string theory have been conclusively dashed, that there as been a fall-back to the argument that “well, we only really care about quantum gravity, weren’t really serious about that particle physics stuff”

2. The problem with the argument that “all we have to do is understand non-perturbative string theory, but it’s just too hard right now”, is that, based on what we do know about non-perturbative string theory, there is zero evidence that it will produce a viable unified model. The situation is quite the opposite: everything that has been learned about non-perturbative effects gives evidence against this, pointing strongly to the conclusion that if any ground states of such a theory lead to a physically sensible theory, an essentially infinite number do, giving a radically non-predictive framework that can’t ever tell you anything about particle physics. This situation is what is driving string theorists into the arms of Lenny Susskind and pseudo-science. The idea that, if we were smart enough, we’d figure out some wonderful new version of M-theory which would explain particle physics has nothing behind it other than wishful thinking.

http://www.math.columbia.edu/~woit/wordpress Peter Woit

Charlie,

The problem with announcing that “string theory is mathematics” is that mathematicians aren’t going to agree to this. As Sean points out, no one even knows what “string theory” is supposed to be, it’s not something well-defined, but a set of conjectures and hopes, many with little backing, about a theory that some people would like to exist.

Physicists are all too willing to dismiss the failure of string theory as due to it being too abstract, and thus “just mathematics”. That’s not the problem with it, the problem is that it’s a wrong idea about unification.

http://blogs.discovermagazine.com/cosmicvariance/sean/ Sean

Title fixed! Sorry about that.

Peter, of course there was a lot of excitement about compactifications and the attempt to derive particle physics from string theory. But the reason why people were ever optimistic about string theory as a theory of everything was because gravity was included. Naturally, if you think you have the correct theory of quantum gravity, you’re curious about how it connects to particle physics. But even if that turns out to be difficult, having the correct theory of quantum gravity is still pretty interesting.

And Charlie, proclamations aside, string theory is physics. It’s a formal hypothesis about how the real world works. Our difficulties in connecting it with observations don’t change its epistemological status.

http://deferentialgeometry.org Garrett

This point should probably be included in the argument:

String theory has failed as a theory of everything because it cannot describe what we know about our universe more succinctly then GR and the standard model can. As Peter points out, people used to think the known particle spectrum was going to come out of strings naturally. But it didn’t. In order to make contact with GR and the standard model — as any ToE must — string theory requires all sorts of baroque mathematical convolutions and assumptions, as well as many additional parameters. It is much more complicated than what it is striving to explain. This is a clear sign of a failed theory.

http://evolutionarydesign.blogspot.com/ island

having the correct theory of quantum gravity is still pretty interesting.

Again with the unproven assumptions… and again I say, prove it.

William Parker

It might be easier to specifically argue against the Landscape.

When the discussion moves from empirical science to pure philosophy, it isn’t correct to assume that scientists are good philosophers. You can find any number of brilliant scientists, now and in history, who can seamlessly move their thoughts from a realm of pure empiricism to pure gobbledy-gook. I know there is no substance to it because you can find many completely opposite directions to the conclusions, and the character of the discussions starts to resemble a religious argument, and we know how productive those are at determining the objective truth. All individuals should recognize that they aren’t immune to the human tendency to start thinking in these directions when the possibility of evidence disappears.

Some things in the universe, including the Cosmological Constant, seem exceptionally tuned. We don’t know why (yet). If String Theory is the ultimate description of the universe, there is reason to suppose we will never know why. The scientific discussion should end there, and now it’s philosophically anyone’s game. Yes, we know of many specific cases where things are exceptionally tuned and we can observe that there is actually a larger landscape of possibilities. It’s not now correct to take this as “evidence” that a landscape of universes “actually” exists. It’s not evidence in any scientific sense, and the supposition is completely equivalent to “it just is”. I’m sorry, but you guys are far smarter than me, but ability and science in science does not project over to pure philosophy any more than it does to politics and policy discussions.

Eric

Garrett,
String theory has not ‘failed’ no matter how many times this bit of propaganda is repeated. It is actually very easy to get models which are very close to the Standard Model by straightforward and simple compactifications, either heterotic or Type II. The whole problem of the landscape is that these compactifications are not unique, at least at the level of perturbative string theory. One would have the same problem in any conventional GUT, say in trying to obtain the standard model from E_8.

http://www.valdostamuseum.org/hamsmith/ Tony Smith

Peter Woit said: “…. in 1984 … the highly cited papers from that era …[had]… a lot about compactification schemes for getting the Standard model. The people who made string theory a hot subject were mostly particle theorists excited by the the idea of a unified theory, with real predictions seemingly possible …”.

Sean disgreed, saying: “… the reason why people were ever optimistic about string theory as a theory of everything was because gravity was included …”.

You can judge for yourself which is the more accurate view,
based on the following:

At the 1984 APS DPF Santa Fe meeting, John Schwarz gave a talk
(on work with Shahram Hamidi) entitled
“A Unique Unified Theory That Could Be Finite And Realistic”,
in which he discussed “SO(32) and E8xE8 superstrings” with respect to finding “the correct low-energy (compared to the Planck mass) theory in four dimensions with which to make contact”.
Swarz went on to say that “In collaboration with J. Patera, we have classified all the chiral N=1 theories that satisfy the one-loop (and hence two-loop) finiteness conditions. The list includes theories based on E6, SO(10), SU(5), and SU(6) that can describe three or more families without mirror partners.
However, if we also require the occurrence of elementary Higgs fields in representations that can give realistic symmetry-breaking patterns, then one unique scheme is singled out. …
The unique model that is potentially finite and realistic is based on the gauge group SU(5).
… The three-loop calculation could result in a dramatic failure and is therefore of utmost importance. …”.

After Schwarz made his 1984 Santa Fe talk, a lot of work was done on that SU(5) structure. For example,in Physics Letters B, Volume 160, Issues 4-5 , 10 October 1985, Pages 267-270, D. R. T. Jones and A. J. Parkes wrote a paper entitled
“Search for a three-loop-finite chiral theory”. Its abstract stated:
“Grand-unified theories have been constructed out of supersymmetric SU5 theories which are finite at one and two loops. We investigate the three-loop divergences in these models and find that they can never be three-loop finite …”

Despite Schwarz’s declaration that his 1984 superstring theory was predictive and testable,
he did not admit defeat upon failure to pass the three-loop test.
His concrete testable superstring theory just morphed into something harder to test,
and since then, whenever superstring theory has failed a test (such as specific searches for supersymmetric partners, etc) it has continued to morph into more and more vagueness (as of now the Landscape),
with its supporters saying such things as that it “… gives us pieces of the theory of everything. All of the pieces have yet to be put together and some remain unknown. …” and that it is “… part of a larger structure that we don’t understand nearly well enough to make contact with the real world as yet …”.

At the same time, models (such as mine) that actually are predictive and testable (and substantially consistent with observations of particle masses, force strengths, and the Dark Energy : Dark Matter : Ordinary Matter ratio) are ignored and even blacklisted from the Cornell arXiv.

Tony Smith

Anon

I don’t think it is convincing enough. The conclusion that one OUGHT to draw from your very nice discussion above, Sean, is that String theorists must be very careful , especially when they report a new result. Unless they come up with a sensible way to test string theory AND show that they understand the larger theory, they shouldn’t claim to.

Jim Clarage

I have a clear memory as a graduate student in at Brandeis university in the late 80’s (1988 I believe) attending Witten’s series of String Theory lectures at Harvard. The subway lines near Cambridge were so clogged from MIT, Brandeis and other academia traffic for this rockstar event that I remember having to walk the last several blocks to get to Harvard.

On arriving to the campus, the event organizers had to re-schedule the venue from a small lecture room to the large public lecture hall.

My clear recollection was that this buzz was because string theory was promising to “predict” the numeric values for fundamental constants in the standard model (such as electron mass, mixing angle, etc.). Gravity was mentioned as further “bonus” of this theory, but definitely particle physics was a main selling point.

I think anyone who recalls their initial interest in the subject has to admit the promise and hype, and yes what made it so alluring to young graduate students in the 80’s, was much more than just quantum gravity.

http://blogs.discovermagazine.com/cosmicvariance/sean/ Sean

Look, I could tell similar stories about people being excited about quantum gravity, and collect all sorts of testimony to back me up. Here’s the thing: it makes absolutely no difference. If Einstein had claimed that GR would lead to an inexhaustible supply of free energy, it would not have affected the truth or falsity or promise of the the theory in the least. The foibles of theorists should not be confused for the problems of theories. Talking about the sociology of physics is interesting in its own right, but has no bearing at all on whether a particular theory is promising or not.

Irate Particle Physicist

The chief benefit of string theory research as I see it is that it may be starting to yield insights into how to understand strongly coupled dynamics of the sort relevant for QCD. Zeus forbid that the LHC discovers new strongly coupled physics at the TeV scale—that would really piss me off.

http://www.math.columbia.edu/~woit/wordpress Peter Woit

Sean,

This is not a question of sociology. It’s about what’s testable science and what isn’t. There were all sorts of reasons people decided to work on string theory, but by far the most important one is that it held out the promise of making real, testable predictions. The problem with pursuing string theory as only a theory of quantum gravity is that it’s not testable. If you believe all the things string theorists would like to be true, not only do they have a consistent theory of quantum gravity, they have an exponentially large number of them. And no way at all to ever test any of them. You can go on about how this makes “absolutely no difference”, that it has nothing to do with the truth or falsity of the theory, but what it has to do with is whether this is legitimate science or not. While an increasingly large number of theorists don’t seem to think this anymore, most scientists are of the opinion that theories that inherently can’t be tested aren’t what science is about.

http://blogs.discovermagazine.com/cosmicvariance/sean/ Sean

The question of why individual scientists in the 1980’s were excited about string theory is certainly a question of sociology. We may argue whether one or another reason is a good one or not, but that is a logically distinct question. If we wanted to drop discussions about what such-and-such a person was thinking when they gave a talk twenty years ago, I’d be all in favor of it.

Thomas Larsson

As usual, it does not occur to string advocates that string theory is the wrong theory of quantum gravity, because there are better and more physical ideas. To see how QFT must be modified to work with gravity, one can argue like this:

Every experiment is an interaction between a system and a detector, and the result depends on the physical properties of both. We are typically only interested in the detector-independent part of the result, which is what theories like QFT speak about. QFT never mentions the detector’s properties, because it implicitly assumes that its charge is very small (so the detector does not perturb the system) and its mass is very large (so the detector follows a well-defined classical worldline, i.e. its position and velocity, as measured by physical rods and clocks, commute). This hidden assumption runs into problem specifically with gravity, because then charge and mass are the same (heavy mass = inert mass).

It follows that any theory which implicitly assumes an infinite detector mass, whether it involves fields, particles, strings, loops or whatnot, will run into trouble with gravity, because an infinitely massive detector will interact with gravity and collapse into a black hole. The solution is in principle simple: the theory of quantum gravity must explicitly depend on the detector’s mass.

I’ve finally figured out why I don’t like your “argument”. You make the blanket statement “The best reason to think that research on string theory is largely a waste of time is because it’s just too hard.” This strikes me as like when people say, eg, “I’m a failure” when they want someone to turn around and say “No you’re not.” (or in this case “No, you should think about hard stuff”). Now this is a good “debating tactic” but I’m think a more convincing “real argument” would be to be more precise about what precisely about the thinking task is “too difficult”.

Scott

As Peter said, that really did not come off as an argument against string theory at all, but as one for it. If the argument is read with a touch of sarcasm it is apparent that this is the case. In particular the last line of the argument is seems designed to make one feel the opposite of the arguments stated goal.

Heres a recap:

1: string theory was at first really promising because with it we might “figure it all out” despite lack of experimental evidence.

2: The fact that it might not be able to make any predictions about particle physics is ok, because it still can be a quantum theory of gravity

3. the difficulty string theorists are having has to do with not knowning the actuall non-pertubative theory that string theory is.

4. There has been a lot of progress towards finding this theory, but the work left to get to the theory is daunting.

5. with our current understanding we can not make any predictions and getting to where we can connect the theory with reality could end up taking a long time.

6. So lets just not try at all since it might end up being so hard that it takes a few centuries.

You imply in 5 that pursuing string theory will eventially connect with reality, which i am going to assume means that it makes testable predictions. Something which is possibly not true.

The fact is, that there are reasons to think that string theory is the wrong aproach to quantum gravity, as well as explanation of the standard model obviously. The best argument for string theory being a waste of time(where waste refers to lack of progress in understanding the physics of the universe) is that string theory is the wrong aproach. Therefore your hypothetical argument should be the best argument for why someone would suspect this to be the case.

Ellipsis

Sean,

Do you think in 1920s they hadn’t predicted that there would be 3 generations of quarks and leptons because the theory was too hard?

Or do you think it’s because it was fundamentally not possible to predict, because our universe is _not a unique manifestation of a physical space_?

The latter is why people are worried about trying to predict a theory of everything at energies 15 orders of magnitude higher than what we probe in the laboratory.

It’s not just that it’s hard to predict, it’s that it’s probably _not predictable_.

Just like Newton couldn’t have developed quantum mechanics with the experimental evidence available in his day. It wouldn’t have mattered if he was even more brilliant than he was.

Harold

Hi Scott – perhaps Sean doesn’t believe that String Theory is the wrong approach and so his best argument against it was really that it was too hard. He mentions he is trying to argue for what he believes in. Ultimately, he doesn’t find those arguments convincing. As far as post being a line of argument for string theory, there might be some bias already knowing that Sean doesn’t believe it.

Harold

I realized that my last use of the word “believe” should be “find it a convincing argument enough to sway his stance.”

Tumbledried

Re Sean #12: You mention that “the reason why people were ever interested about string theory as a theory of everything was because gravity was included”. However, I should point out that the problem is not that you can embed gravity into a theory with planck order effects, but that somehow you have a means to select the correct embedding, rather than simply picking one which takes your fancy. For instance, consider the flat space Lagrangian for a manifold M in GR:

int_{M}R

One can simply introduce a number of extra terms, to form a naive perturbation expansion for a theory of QG:

int_{M}(R + epsilon L_{1}g + epsilon^{2} L_{2}g + …)

where epsilon is your “planck scale” parameter and the L_{i} are differential operators acting on the metric g (maybe my notation is a bit off, but you get the idea). It is clear that this is legitimate if you are considering low energy physics, eg particle physics, since then quantum effects will be perturbations about the norm, provided the L_{i} are bounded operators.

But then we now have an action, or rather, a whole family of actions, that all “include gravity”! So, if I follow your reasoning correctly, these must all be valid theories of quantum gravity.

Scott

Harold, I thought the whole point was to make arguments for things you don’t believe, that are supposedly better then those made by most people who do believe them. So he should be able to make an argument for string theory being a wrong approach to quantum gravity. This is also more accurately what those he disagrees with are arguing for.

Also did you mean to imply that my bias was making me read into Sean’s argument an argument against not being a waste or that it was Sean’s bias making his argument counterproductive? I suppose both did exist, but I still maintain that the argument is of that nature. For instance after making the point that it seems to fail to make predictions about standard model parameters, why would you then dismiss this entirely, instead of just moving on to why the quantum gravity aspect is a waste of time as well(because it hard.) While his argument would still stay the same, it is obviously more persuasive to simply argue againsts both possible benefits then to argue against one, then make the argument your adversary might make(will that doesn’t matter because…) before then going on to argue against that as well.

The second half of his argument, is essentially arguing that the non-perturbative theory can be found or at least well understood enough to connect with reallity(testable predictions), something that alone would be considered an argument in favor of string theory research, but then goes on to say that since it is hard it might take a long time perhaps even centuries(though this seems presented as an extreme case) and so we shouldn’t even bother.

All he has to do is add to the end “… too hard, one would think, however it could very well not take that long.” and now we have a clear argument for it not being waste, simply by stating something that had already been implied in the precceeding paragraph.

Hi again Scott – I mean to say: Although he is making arguments against what he believes in, he still believes in his arguments. So then the best argument he believes in is that research of this topic is too hard. Also, I don’t mean to imply that you specifically have bias, but that it might be tempting (whether the temptation is well-deserved or not) for people to see Sean arguing for the opposite side. I do see your point and it is possible with some imagination to see how Sean is really arguing for String Theory. In any case, I think what he did is a fun exercise and I’ve been meaning to try (coincidentally juts days before) to do the same for the statement I made in his previous post – that going into particle physics is a bad idea.

manyoso

“it’s the connections between “deep down” and the world around us that are the hard part.”

And you take it on FAITH that any such connection exists. There are no guarantees that M-Theory, once we’ve figured out what it is, will provide any connection to the real world. There are no guarantees that M-Theory will turn out to be an adequate model of real world physics. It might just be an elaborate contraption that thousands of physicists have wasted hundreds of man years of time to find out it is just a fantasy model of a non-existent universe.

JVG

Good morning. Perhaps the exercise would yield better results if more concentration were put on principal than particulars. While particulars are necessary for purposes of example, an argument without principal fails to meet its created intent.

A suggested starting point relative to the use of string theory: why knowledge?

http://golem.ph.utexas.edu/~distler/blog/ Jacques Distler

The trouble with arguing that String Theory is inherently unpredictive about particle physics, as opposed to merely being too hard, is that it’s not a statement that follows from what we currently know about the theory. It may turn out to be true, but as I explained in a previous CosmicVariance “String Wars” comment thread (see also the followups: I,II,I,I,I,I), there are equally plausible scenarios in which one will ultimately be able to extract highly predictive statements about particle physics (but not, say, the cosmological constant) from the theory.

Since we don’t know how this will play out, it’s perfectly plausible to posit a worst-case scenario (the String Theory Landscape will turn out to be entirely unpredictive about particle physics) and ask whether it would still be worth working on String Theory.

But if you’re going to do that, you need to weigh all the other reasons to be interested in String Theory (e.g., the applications of AdS/CFT to RHIC physics), as opposed to simply looking at those things which may or may not have motivated people to take up the subject 20 years ago.

I guess you’re going to tell us next that your worst defect is being too smart….

In the meantime, the advent of sexy new data from the LHC and

This is the part I just cannot understand. I’ve heard similar statements from many string theorists. They don’t seem to realize it just does not make sense. It’s like saying, “in the meantime, people will keep playing with science, while we await the second coming of Jesus Christ”. Well, it’s not at all obvious that Christianity is the true theory and science is just a pastime to make the wait less boring.

Snarkalicious

“equally plausible scenarios in which one will ultimately be able to extract highly predictive statement”

And there are equally plausible scenarios in which one will ultimately be able to extract highly predictive statements out of Jello Theory in which we posit the universe is made of tiny clumps of jello. Just because we don’t *know* what the Jello Theory really *is* yet or how to connect it to the real world doesn’t mean people shouldn’t wonder about it. After all, it could turn out to be highly delicious for all of us!

ragtag

plausible scenarios in which one will ultimately be able to extract highly predictive statements about particle physics (but not, say, the cosmological constant) from the theory.

to
This seems perfectly sensible. I’d only add that this is only half of the story. High predictivity leads to predictions which, even more importantly, must be correct. This is where experimental data comes in, and it is as relevant to ST as it is to any other theory. After all, the way to natural laws is paved with good theories.

Hag

I think Sean should have left this item as the last.

Scott

Harold, the point is that something maybe being too hard(note that he never bothered to make the case that it is to hard, just that it might be) is not a convincing argument, despite his declaration of “Pretty convincing, eh?” Arguing that it is a waste of time because it is hard is a fundamentally different argument then it being a waste of time because it is wrong/ not even wrong. This is supposed to be an improvement on the arguments of those who actually take the position. Second he doesn’t believe it is to hard, he allows for the conclusions to not warrant the conclusion and he could do the same with it being a wrong or at least bad approach.

This would be equivalent to if for “God exists” argument he argued for an existance as an idea rather then as people think he exists as part of/the creator of reality. It is disengenous to pretend he is arguing about the same thing as Woit, Smolin and others.

http://thedialogs.org Alex Na

“It is too hard”

What is too hard? I mean any problem you don’t know the algorithm to solve is hard. Beyond that, how do you differentiate the levels of hardness?

It is all in the realm of unknown and the main attribute of it is being unknown So we just do not know how hard it is. There is a chance someone tomorrow ( or next year) will show all of us how simple (OK, not that hard) it is.

I am just trying to be optimistic here.

Great blog. Just subscribed.

Jason Dick

Alex Na,

A large number of theoretical physicists have tried for a few decades now to understand what string theory implies about reality without success. This isn’t to say that we’ve learned nothing at all about string theory. But what we have learned hasn’t told us anything about any observations we might make, despite the very large number of man-hours employed in understanding it. So string theory is definitely “very hard”. But whether or not it’s too hard is clearly a judgment call.

I guess I haven’t heard of any more promising theory for quantum gravity, so I don’t see why theorists shouldn’t keep trying to understand string theory. From what I understand, we are essentially guaranteed to understand more about mathematics anyway just by pursuing string theory, mathematics that will be useful whether or not string theory turns out to be accurate.

String theory isn’t exactly a waste of time, but it shouldn’t be the only approach to solving the unsolved problems of physics. It seems to have stopped Physicists from thinking outside the box and instead try to come up with more and more spin to sell it despite the problems it encounters.

My points would be:

1) Its not a theory – no equations, no way of proving true / false
2) Its not one theory, its 10^500 or more, if you subscribe to the landscape, with so many theories one is bound to describe our universe, you just need to plug in the right 500 numbers (as opposed to a factor of ten less constants in the SM)
3) Its not background independent, so can never describe a changing spacetime geometry as required by GR
4) It moved from a hadron theory to a quantum gravity theory because it described the graviton. But gravity is not a force in GR, it’s paths through a changing geometry to preserve minimal PE, why do we even need a graviton?

http://beingdeveloped Colin C Ware

There is much discussion on myriad aspects on the Theory of Everything (TOE). I have been seeking the conditions that will define, at the least, forms of a — the — basis for developing a true, non-theoretical description of TOE. I strongly believe that certain physical properties will be included in this base or foundation for building toward TOE. What will these be?

What drives us to pursue TOE? I came onto this blog asking Google “benefits of knowing the theory of everything”. Behind this search are my questions such as: What specific physical elements or properties will be inter-related? How will they be related? That is, what form of theory-less equations and supporting statements will do this? Perhaps TOE will not be “completely” defined, but what would be sufficient to point us in the “correct?” assured direction?

http://dftuz.unizar.es/~rivero/research Alejandro Rivero

Time ago in other similar thread Baez was arguing against the theorem “spin2=graviton”. Let me pursue this “no graviton theme” further: suppose we can compactify strings to 4D in a way (say, NCG or some retorted nogeometric thing) that there is not spin 2 particle down there: then string theory could still be a supersymmetry theory of gauge interactions. Furthermore, suppose it works and it predicts all the susy parameters. Should it to *disproof* string theory?

As a minimum, as it does not include gravity anymore, it is an argument for the restricted idea “Research on String Theory is Largely a Waste of Time for Quantum Gravity”.

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Cosmic Variance

Random samplings from a universe of ideas.

About Sean Carroll

Sean Carroll is a Senior Research Associate in the Department of Physics at the California Institute of Technology. His research interests include theoretical aspects of cosmology, field theory, and gravitation. His most recent book is The Particle at the End of the Universe, about the Large Hadron Collider and the search for the Higgs boson.
Here are some of his favorite blog posts, home page, and email: carroll [at] cosmicvariance.com .